BMC Medical Research Methodology BioMed Central Debate

Background Randomised controlled clinical trials are performed to resolve uncertainty concerning comparator interventions. Appropriate acknowledgment of uncertainty enables the concurrent achievement of two goals : the acquisition of valuable scientific knowledge and an optimum treatment choice for the patient-participant. The ethical recruitment of patients requires the presence of clinical equipoise. This involves the appropriate choice of a control intervention, particularly when unapproved drugs or innovative interventions are being evaluated. Discussion We argue that the choice of a control intervention should be supported by a systematic review of the relevant literature and, where necessary, solicitation of the informed beliefs of clinical experts through formal surveys and publication of the proposed trial's protocol. Summary When clinical equipoise is present, physicians may confidently propose trial enrollment to their eligible patients as an act of therapeutic beneficence.


Background
What does the term 'interim analysis' mean? A short definition is that it refers to the repeated analyses of data as they accumulate. This is not a bad definition, since it can be applied not only to clinical trials but also to laboratory experiments.
Why does it matter? It matters in a statistical sense that is not very different from that of making multiple comparisons within the same experiment. In either case, the risk of Type I error (false-positive inference) increases progressively as the number of tests of significance increases. I have reviewed elsewhere the problem of making multiple comparisons and ways of solving it [1,2]. Here I review the topic of making serial comparisons on data as they accumulate. To state this problem in a very crude, but nonetheless broadly accurate, fashion it is almost inevitable that if the outcome is on the borderline of significance, the outcome P ≤ 0.05 will ultimately occur -quite falsely -if enough repeated interim analyses are made.
In the context of clinical trials, the issue of interim analysis is not a new one. It has been discussed in the statistical literature since the 1960s, and has reached the level of consciousness of clinical trialists over the last few years. For instance, the number of 'hits' in a PubMed search (National Library of Medicine, Washington DC) that I conducted for (interim AND analysis) were: 1968-70 (0), 1978-80 (10), 1988-90 (67), 1998-2000 (214). In 2001-2003 there were 252 hits. In the earlier periods, papers dealt chiefly with theoretical issues. In the later periods, most were concerned with actual clinical trials.

Clinical trials
Several statistical techniques for dealing with interim analyses of clinical trials have been described. These include, in order of appearance, the Armitage-McPherson [3], Pocock [4,5], Haybittle-Peto [6,7] and O'Brien-Fleming [8] methods. All these techniques depend on the interim analyses being planned in advance. Excellent, simple descriptions of these can be found in the book by Friedman et al. [9]. A simulation study suggests that the O'Brien-Fleming technique is the most powerful of these [10]. Lan & DeMets introduced the notion of the adaptive, α-spending, function, that could be applied to unplanned interim analyses [11,12]. However, this has been severely criticised by theoretical statisticians [13]. Then there is the Bayesian approach, well-described by Jennison & Turnbull [14], but rarely employed.

Laboratory experiments
None of the techniques for interim analysis of clinical trials is applicable, or easily adaptable, to the unplanned statistical analyses of laboratory experiments, usually undertaken covertly rather than overtly.
There are good reasons and bad reasons for performing interim analyses of laboratory experiments.
A good reason is that the investigators have made, in advance, an estimate of minimal group (sample) size. But they are not confident that it is a good estimate. This may be, for instance, because they have had to base their esti-mate on others' published data or because it is based on a small set of pilot experiments. It is reasonable, therefore, that they should analyze the results when their estimated minimal group size has been attained. If their null hypothesis is rejected, they can stop. If not, they can then use these results to re-estimate minimal group size and carry on.
A bad reason is that the investigators have not formally estimated minimal group size, but have merely made a guess. They carry out the first round of experiments, test the results, and find that they are not quite 'significant'. So they do a few more experiments. Still not quite there. So they do a few more experiments -and so on until they achieve P = 0.05, or give up.
What solutions are there to this problem? One is to employ relatively simple methods for adjusting the critical value of P. An altogether different approach is to use a technique called matched-pairs sequential analysis. A third approach, already hinted at, is to re-estimate minimal group size.

Simple methods for adjusting the critical value of P
The Šidák inequality [15] plays an important role in multiple comparison procedures [1,2]. This means that the adjusted critical value of P is given by the formula 1 -(1 -P) k , where k is the number of interim analyses and the nominal critical value of P is usually 0.05. Alternatively, the raw P value resulting from a test of significance can be adjusted by the formula P' = 1 -(1 -P) 1/k . The Šidák adjustment is a severe one (Table 1). Why is this? It is appropriate for multiple comparisons when these are completely independent. But it is obvious that successive interim analyses are not independent of each other, but to some degree correlated. This is also true of many (most) sets of multiple comparisons [2]. For this reason the Šidák adjustment is unsuited to planned interim analyses. However, it may have a place for the single, unplanned, interim analysis when, to put it bluntly, the investigators should pay a high penalty. The Armitage-McPherson adjustment [16,17] is a little less severe than the Šidák adjustment (Table 1), but has the same drawback that independence of the interim analyses is assumed.

Matched-pairs sequential analysis
This technique is attributed to Wald [18]. He was able to publish it only after World War II because during the war it had been classified as an economical and sensitive technique for testing munitions. Armitage suggested it as a technique for use in clinical trials [19,20]. However, it has been used infrequently in this connection, for reasons given below. Kilpatrick & Oldham were the first to use the technique in an actual clinical trial [21], though in a rather crude, one-sided, fashion. An interesting example of its use is in a clinical trial of the therapeutic efficacy of prayer [22]. My own experience with it is confined to a trial of the efficacy of rose-preserving solutions (see Fig. 1) [23].
An example of matched-pairs sequential analysis [23]   Matched pairs of subjects are assembled, and the members of each pair are assigned randomly to one or the other treatment to be investigated. The analysis is graphical. Horizontal, V-shaped, statistically-defined, upper and lower boundaries are constructed. The outcome of the trial for each pair is scored as a preference for treatment A or treatment B, and entered into the graph. If the zigzag line described by successive pairs crosses one or the other boundary, it can safely be concluded that A is superior to B (or vice versa) at a specified nominal level of significance (for instance, two-sided P = 0.05). In the preferred closed, or restricted, design a third boundary is placed across the open end of the V. If this is crossed first, then at a specified Type II error-rate it can be concluded that there is no significant difference between the treatments [20]. The advantage of this approach is that both the Type I and Type II error-rates are controlled, and the maximum number of matched pairs necessary to cross one or another boundary can be predicted. The coordinates of the graphical boundaries are determined by: (a) the selected two-sided Type I error-rate (2α = 0.05, 0.01); (b) the selected Type II error-rate, β, where (1 -β) = power to reject the null hypothesis; and (c) the θ statistic. Typical values of these are 2α = 0.05 or 0.01, β = 0.05, θ = 0.90 (see Fig. 1).
The strength of the matched-pairs technique is that it ensures that an inference will be reached (A>B, B>A or A = B) with a predictable maximum number of paired subjects. However, it has serious practical limitations that have greatly restricted its use in clinical trials. These are that: (a) there must be a large reservoir of eligible patients so that matching can be done; (b) the time from entry to outcome must be short compared with the expected duration of the trial; and (c) the technique cannot be applied to tests on survival curves such as the logrank (Mantel-Haenszel) test. For these reasons, group sequential analy-sis has been the technique preferred for clinical trials [24][25][26].
If even amateur biostatisticians follow the instructions given by Armitage [19,20], they should be able to design the graphical boundaries for a closed (restricted) matched-pairs sequential analysis. If they (or reviewers) have doubts about the outcome, they can use an exact test on a single binomial to confirm the inferences (see Fig. 1).
I have been unable to find an example of its use in laboratory experiments, with the exception of my obscurelypublished trial of rose preservatives [23]. Yet there is an almost unlimited supply of laboratory animals that can be matched for characteristics such as sex, age and weight. The outcome of the experiment is usually available within hours, days or weeks. The only reservation is that if the outcome of the experiment is measured on a continuous scale, there may be some loss of power because for the purpose of graphical analysis the outcomes are converted into a binomial preference for one treatment over another.
Later, Armitage and colleagues [16], and McPherson & Armitage [3] addressed the matter from a somewhat different perspective and by different statistical techniques. They called this 'repeated significance testing' (RST). The requirement of matched-pairs remained, but they calculated (or obtained by simulation) the actual significance levels corresponding to nominal levels for serial repeated testing, for both binomial and continuous (normally-distributed) outcomes. This results in parabolic boundaries, rather than the linear boundaries of Fig. 1 [3]. If N (the number of matched-pairs) is greater than 10-15, the parabolic and linear boundaries are very similar. An example of their work is in Table 2 and Figure 2. If the outcome measure is normally-distributed, the RST approach is to be preferred. If investigators consider using this, it is best that they consult an experienced biostatistician. Armitage gave an easily-understood account of the matched-pairs technique in 1975 [20]. His book is out of print, but is available in libraries. Alternatively, biomedical investigators and biostatisticians can consult the original accounts [3,16,19], or Whitehead's book [24].

A third approach
In planning a prospective clinical trial, it is mandatory that minimal group sizes are estimated before the trial starts. This is insisted on by institutional human ethics committees.
Institutional animal ethics committees, at any rate in Australia, now also insist that minimal group sizes are estimated in advance. This can be done on the basis of earlier studies in the same laboratory or, second best, studies published by others. The convention is to make the estimate on the basis that the critical value of P is 0.05 at a power of 0.80 (80%). Very useful aids to making these estimates are published tables [27], or interactive computer programs (for instance, nQuery Advisor, Statistical Solutions, Boston MA).
But minimal group size estimates are only as accurate as the data on which they are based. Often these data are suspect, or the dataset is too small. So when investigators have done the necessary number of experiments, analysed the results, and find that P is just a little greater than 0.05, it is not unreasonable that they should re-estimate minimal group size on the basis of these experiments. If the new estimate exceeds their original one, it is not unreasonable that they should carry out further experiments so that the revised estimate is achieved. Then, it is argued, their new and definitive analysis needs no adjustment of the P value.

Summary
There has been a twofold purpose to this review. One has been to remind clinical investigators of the rules governing the interim analysis of results as they accumulate in clinical trials. These rules are very firmly established, thanks to the work of biostatisticians and of regulatory bodies. The second, and more original, reason is to acquaint biologists who are conducting laboratory experiments with the price they should pay for analyzing their results as they accumulate, usually to decide whether they need to do more experiments to 'achieve' a magical P = 0.05. Whenever I chastise experimentalists for conducting interim analyses and suggest that they are acting unstatistically, if not unethically, they react with surprise.
I hope that this review may bring experimentalists and clinical trialists closer together in their attitudes towards the interim analysis of accumulating results. I believe that laboratory experimenters have a good deal to learn from clinical trialists. In particular, I commend to them matched-pairs sequential analysis as a technique for designing and analyzing their experiments.
Redrawn from Fig. 5.3 of Armitage [20], with the kind per-mission of Blackwell Publishing